This is a guest post by Prof. Jim Schombert
Greetings Stacy’s blog readers! My name is Jim Schombert, I’ve been working with Stacy for about a quarter of a Hubble time. I knew him when his hair was brown.
In any case, I asked him if I could make a contribution to the dark matter discussion. Partly this is motivated by the LUX-ZEPLIN ‘detection’, but also cause there are some clear red flags from a philosophy of science viewpoint. I was a philosophy major in college, switched to astronomy when I 1) realized there was no money in philosophy, and 2) people at parties would talk to an astronomy major, not so much a philosophy major. I never lost my interest in the philosophy of science, tried to keep up with the literature, so how should we view the current MOND vs dark matter debate from a philosophical view? (and for a more sophisticated analysis of the topics below, I direct the reader to Merritt’s superb books and articles on MOND).
There are basically two types of philosophers when it comes to science, one type is heavy in mathematical logic and deep discussions of foundations of science, the other type is more concerned about how science is done, i.e. the history and impact side of science. All of us know the key writers of this second type of philosophy of science; Popper, Kuhn, Lakatos (hereafter PKL). You will know them cause when you read their works you will immediately recognize yourself and colleagues in their descriptions. You basically have this strong sense that we operate on our data and computer simulations just as described by these famous thinkers. In short form, Popper = ‘falsification’, Kuhn = ‘paradigms’, Lakatos = ‘research programs’, we will expand upon this below.
We all know there is no ‘truth’ to our science, you can never prove a scientific idea, you can only test it, hard, in an attempt to falsify it (Popper). The more the idea stands up to testing, the ‘stronger’ it gets, where stronger means more used/accepted by the community. Paradigms (Kuhn) are now thought of more as frameworks (think Newtonian mechanics), and research programs (Lakatos) are like giant factories of ideas that define how we come up with new ideas to test. Key to all this was that PKL insisted that this only worked when discussing the history of science, and the philosophy community was deeply disappointed in the works of PKL because they wanted criteria that could be applied in the moment (i.e., some system to assist the science community in directing science to more productive methods and goals). It’s obvious to all of us (who have been doing science for awhile) that this description is more of an idealization and usually doesn’t work (pick any observing or funding review panel as an example of how this just fails in the moment, but works well in retrospect).
Let’s take a very simple example (that almost everyone is familiar with) to see how the methods proposed by PKL work best in hindsight and are fairly useless in the moment. Consider Newtonian gravity in the mid-19th century (by the way, did you know that Ptolemy’s system of epicycles was used by the makers of almanacs into the 20th century? The math was simpler and just as accurate as using Newton. But I digress). So, a wobble in the orbit of Uranus. Abandon Newton? Hell no, the framework/paradigm has solved so many problems. Consider an auxiliary hypothesis, i.e. another planet. Right there, Neptune! Boy, how strong is your paradigm that predicts new planets. Better telescopes, more accurate data, hmm, wobble in Mercury. Obviously, try the same hypothesis (the so-called planet of Vulcan). Nothing found, fortunately relativity came along pretty soon (although it’s goal was not to solve Mercury’s orbit, it had bigger issues to address). Newtonian physics survives, but now with limits on its applications (stick to low energies). In the moment, it was hard to see the depth of the problem or the need for radical change.
In any case, us working astronomers immediately recognize this kind of scientific effort; the nuts-and-bolts, thinking about new ideas, new technology, new data – in our own research. Now let’s turn to the dark matter paradigm. For the readers of this blog, I don’t need to discuss the details of the LCDM paradigm. In brief, Oort discrepancy (1960’s), flat rotation curves (1970’s), cluster M/L’s (1980’s), large scale structure (1990’s) and, of course, the capstone CMB+BBN+Omega_Lambda (2000’s). Historically, its important to remember that a great deal of work in the 1980’s eliminated anything made of baryons for CDM (low mass stars, black holes, planets, rocks, etc). In fact, most of us stopped even trying to explain CDM by the launch of HST, there were more interesting problems to address. We just took CDM as a black box solution; those interacting galaxy simulations looked amazing.
In the end, CDM was expected to be a gravitationally interacting, not short-lived, not hot, non-baryonic particle. With the closure of the SSC in 1992, a large number of particle physicists were suddenly out of jobs, dark matter looked like the clearest path to reach new physics (and a paycheck). And astronomers were just as guilty, Fig. 1 is a old plot from an Oemler workshop paper showing the state of the art in 1985. Notice the implication that dark matter could close the Universe (i.e., Omega = 1 all in mass; there was no Lambda back then). And a closed Universe was, for some reason*, a massive desire for the astro theoretical community. And we see the beginnings of how cosmological issues override galaxy issues for the community (there’s a nobility to doing cosmology, galaxies are dirty).
There is also no need to re-iterate the failure of the high energy community to find any dark matter particles. The amount of money and people in CDM makes the Manhattan project look like a garage shop effort (only CDM did not deliver a new weapon by the 2020’s). During this time, a few of us noticed that the baryons in galaxies were strongly tied to the ‘dark matter’. We were told that low mass dwarf galaxies were dark matter dominated, but a few of us mentioned that they are also strongly gas dominated, i.e. how did the dark matter know to dominate in galaxies with the highest gas fractions? These kinds of anomalies began to build up for observers, didn’t really appear in the theory papers.
Now let’s consider how PKL would interpret the current status of the dark matter paradigm. The emphasis by all three philosophers was to examine the historical record. This frustrates mainstream philosophers who would, ideally, like apply some criteria to the current state of affairs rather than only look at hindsight. But there may be enough historical record to, at least, determine the current trajectory for the dark matter paradigm.
Perhaps the first ‘crisis’ to the LCDM paradigm would be the discovery of the baryonic Tully-Fisher relation. The luminosity Tully-Fisher, which was only a measure of the stellar mass by way of stellar luminosity, was not very surprising to the astro/physics community for a larger galaxy would have more stars and dark matter, thus higher rotation velocities. The mass discrepancy was obvious, vindicating the need for some sort of invisible dark matter, but the scatter was large and the relationship was distinctly non-linear at the low mass end. However, the TF relation was well mapped at the high mass end (early-type cluster galaxies) and was extremely useful at locking down cluster distances and mapping large scale structure.
It was Stacy’s superb observer’s insight to think about adding the gas mass to the stellar mass producing a total baryon mass to compare to the rotational velocity (I helped a little, the so-called BTFR). I say ‘observer insight’ for its one of those things that if you work at optical and radio telescopes you are comfortable thinking in terms of different kinds of data, and at ease turning luminosities into stellar masses (i.e., M/L) and HI fluxes into gas masses (lots of details, but that’s what data reduction and analysis is all about). The scatter was greatly reduced and the relationship was increasingly close to a linear fit in log-log space. Regardless
of your MOND vs dark matter bias, the BTFR quite simply says the total baryon mass is related to the total dark matter mass, which would make sense if you scoped a piece of the early Universe (equal proportions of baryons and dark matter) and made a galaxy.
But that’s not how galaxy formation was suppose to work (you don’t scope a piece of the Universe, those CDM halos form first, baryons fall in later), and this baryon-dark matter relationship varied in a surprising coherent fashion across Hubble types. Stacy being a deep reader of obtuse literature in the 80’s taught us that this type of behavior was exactly predicted by basic MOND, especially for the galaxies in my new LSB catalog (to which I remember responding “You’re using my galaxies to disprove Newton? Only death can save you from my wrath”). While MOND was designed to explain flat rotation curves, its key underlying premise is that there is no dark matter, baryons decide how things move, which is what the BTFR said.
Now, in a strictly Popperian methodology, is the BTFR sufficient to falsify the dark matter paradigm? No, of course not, as Kuhn points out, a paradigm that has been so successful in making predictions, and offering research paths, is not simply dropped, that would be intellectually short-sighted. There a lots of historical examples in science to support the continued investigation into dark matter after the discovery of the BTFR. In the field of electromagnetism, one does not actually observe the magnetic fields, we observe its effects and build tools to explore its behavior and derive out rules, theories and models. There is nothing unbalanced about studying invisible dark matter.
In a Popperian fashion, we continued to ‘ruthlessly test’ the BTFR with better samples, improved stellar population models, improved distances. The BTFR survived all this examination, although it risked refutation at every point (for example, many claims that it deviated from a linear power-law fit at the low and high mass ends). The current version by Duey et al. (2026) is by far one of the tightest corrections in astronomy, especially considering all the possible underlying astrophysical processes (e.g., feedback) that could easily distort any kinematic relation. And, as often stated, the slope is 4 and MOND predicted 4, before we looked.
By the time of the BTFR discovery, the CDM community was deep into normal science mode. As Kuhn would state, lots of problem-solving, training students, textbooks and workshops to give. However, MOND was having its breakthroughs. The second crisis will occur with the SPARC sample where Federico Lelli showed that not only does the total baryon mass determine the total dynamical mass (BTFR), but also on the local scale within a galaxy, the baryon density is also correlated with the kinematics point by point within a galaxy’s gravitational potential. This will become the awkwardly phrased radial acceleration relation (RAR).
The smooth change, in acceleration space, displayed by the RAR is well predicted by MOND, but is difficult to explain/reproduce in LCDM without feedback from star formation processes. And the process of adding ‘feedback’ to CDM simulations begins to feel a lot like adding epicycles to ‘save the phenomenon’. Kuhn would say that we need a shift to a new disciplinary matrix, which asks new questions, and will recognize the competence of these new baryon-to-dark matter connection. But to threaten the paradigm, anomalies like RAR and BTFR must persist across different methods, resist easy explanation, and be critical to central themes. Which they seem to do, for many observers, not so much in the theory community.
Theorists, understandably, resist the MOND framework for 1) must explain more, 2) make more precise predictions, 3) coordinate research and 4) open new avenues. These criteria were not met. Also, switching to Milgromian physics will require a complete re-training of techniques, tools and students. A huge investment in time and effort that does not immediately appeal to the theory community given the success of decades of galaxy simulations.
To most of the community, the discovery of the BTFR and RAR do not ‘feel’ like a Kuhnian science revolution seen in the historical record (e.g. Galileo discovering the phases of Venus). A better explanation of the state of current affairs is to adopt the ideas of Lakatos. The heart of Lakato’s philosophy is the role of research programs. A research program is a more expansive view of Kuhn’s paradigms that includes much of the day-to-day operation of science; teaching, grants, textbooks, workshops, presentations. For Lakatos, it was all about whether a research area was progressive or degenerate (possibly even in a zombie stage). To be progressive, for Lakatos, the dark matter framework must be predictive, successful, expanding, yet CDM appears to be in ‘zombie’ stage, ceasing to generate novel predictions, responding to failure with ad hoc adjustments, and no clear path to increase its value as a line of thinking.
MOND work seems more progressive, clean explanations for new discoveries. But it also is struggling, the path forward is not obvious. The accelerated galaxy formation model is the most interesting discovery, and maps into our newest technology, JWST. However, it has been extremely difficult to acquire funding or observing time to address MOND ideas. It’s surprising how conservative funding and telescope panels have become (let’s do one more H_o project). The risk/reward dynamic is clearly in MOND’s favor, but not until more MOND worker are appointed to review panels. I know what I’m talking about, I ran NASA ADP review for two years. So many smart people in one room, overwhelmed by the work, reduced to the easiest path of proposal ranking.
I predict the near future will be one of continued stagnation of CDM research, no progress with many excuses. Some of the excuses looking like new physics, some perhaps even getting the fever that string theory had. The ‘successes’ for CDM have all been indirect (my observations are completely explained by X type of CDM, rather than here are my observations of X type of CDM). And there is still a role for CDM to play in astronomy. Since MOND has a non-linear Poisson equation, it does not lend itself to N-body simulations with ease. And N-body work using CDM has been extremely successful in our understanding of tidal features in interacting galaxies and shell galaxies. It just has to be remembered that when one uses CDM in your simulation, you are basically allowing a proxy for different gravity, and you call it CDM. Kinda of like the softening parameters using early N-body to avoid the wacky math singularities as ‘particles’ in your galaxy simulation got too close.
*Inflation. It was Inflationary cosmology that insisted on Ωm = 1, and theorists chugged that Kool-Aid hard – Stacy
